The idea of the experiment was to find correlations in quantum gravitational fluctuations of space-time by using two very sensitive interferometers and comparing their measurements. Quantum gravitational fluctuations are exceedingly tiny, and in all existing models they are far too small to be picked up by interferometers. But the head of the experiment, Craig Hogan, argued that, if the holographic principle is valid, then the fluctuations should be large enough to be detectable by the experiment.

The holographic principle is the idea that everything that happens in a volume can be encoded on the volume’s surface. Many physicists believe that the principle is realized in nature. If that was so, it would indeed imply that fluctuations have correlations. But these correlations are not of the type that the experiment could test for. They are far too subtle to be measureable in this way.

In physics, all theories have to be expressed in form of a consistent mathematical description. Mathematical consistency is an extremely strong constraint when combined with the requirement that the theory also has to agree with all observations we already have. There is very little that can be changed in the existing theories that a) leads to new effects and b) does not spoil the compatibility with existing data. It’s not an easy job.

Hogan didn’t have a theory. It’s not that I am just grumpy – he said so himself: “It's a slight cheat because I don't have a theory,” as quoted by Michael Moyer in a 2012 Scientific American article.

For what I have extracted from Hogan’s papers on the arxiv, he tried twice to construct a theory that would capture his idea of holographic noise. The first violated Lorentz-invariance and was thus already ruled out by other data. The second violated basic properties of quantum mechanics and was thus already ruled out too. In the end he seems to have given up finding a theory. Indeed, it’s not an easy job.

Searching for a prediction based on a hunch rather than a theory makes it exceedingly unlikely that something will be found. That is because there is no proof that the effect would even be consistent with already existing data, which is difficult to achieve. But Hogan isn’t a no-one; he is head of Fermilab’s Center for Particle Astrophysics. I assume he got funding for his experiment by short-circuiting peer review. A proposal for such an experiment would never have passed peer review – it simply doesn’t live up to today’s quality standards in physics.

I wasn’t the only one perplexed about this experiment becoming reality. Hogan relates the following anecdote: “Lenny [Susskind] has an idea of how the holographic principle works, and this isn’t it. He’s pretty sure that we’re not going to see anything. We were at a conference last year, and he said that he would slit his throat if we saw this effect.” This is a quote from another Scientific American article. Oh, yes, Hogan definitely got plenty of press coverage for his idea.

Ok, so maybe I am grumpy. That’s because there are hundreds of people working on developing testable models for quantum gravitational effects, each of whom could tell you about more promising experiments than this. It’s a research area by name quantum gravity phenomenology. The whole point of quantum gravity phenomenology is to make sure that new experiments test promising ranges of parameter space, rather than just wasting money.

I might have kept my grumpiness to myself, but then the Fermilab Press release informed me that “Hogan is already putting forth a new model of holographic structure that would require similar instruments of the same sensitivity, but different configurations sensitive to the rotation of space. The Holometer, he said, will serve as a template for an entirely new field of experimental science.”

An entirely new field of experimental science, based on models that either don’t exist or are ruled out already and that, when put to test, morph into new ideas that require higher sensitivity. That scared me so much I thought somebody has to spell it out: I sincerely hope that Fermilab won’t pump any more money into this unless the idea goes through rigorous peer review. It isn’t just annoying. It’s a slap into the face of many hard-working physicists whose proposals for experiments are of much higher quality but who don’t get funding.

At the very least, if you have a model for what you test, you can rule out the model. With the Holometer you can’t even rule out anything because there is no theory and no model that would be tested with it. So what we have learned is nothing. I can only hope that at least this episode draws some attention to the necessity of having at mathematically consistent model. It’s not an easy job. But it has to be done.

The only good news here is that Lenny Susskind isn’t going to slit his throat.

Without a model, one really can't say what would or wouldn't test it. But roughly speaking he is saying that he wants to look for correlations and for that you need two interferometers. That is after the GEO600 noise vanished he changed his mind about how to test for the noise.

Sabine,Here we have results, bearing on the structure of space-time and obtained by a very excellent team of experimental physicists. You quantum-gravity phenomenologists had many years to cook up some models that would be constrained by these data. Do you want to tell me that this was impossible? Then prove it. If you can't, it was just a lack of fantasy, or, more likely, a deplorable refusal to do your job. If Craig's experiment doesn't teach us anything about quantum gravity, yet, it's not his fault (he delivered) but of you quantum-gravity theorists.

Full disclosure: I know a few of the experimentalists working on this project.

The Holometer has been looking for correlated noise in co-located interferometers since the beginning of the project. I can't pretend to understand the theory (or lack thereof) at all, and I agree that the experiment has been way overhyped, but demonstrating an absence of correlations in a pair of Michelson interferometers at the level of 10^-40 m^2/Hz is a pretty significant technical achievement. Sensitivity to spatially correlated but extremely weak effects could be useful for e.g., light bosonic dark matter searches.

The experiment required the efforts of < 10 scientists and students and a fraction of a rounding error in the liquid argon neutrino R&D budget. I'd say this is money well-spent.

I have a bit of sympathy for Dr. Hogan in that his approach is similar to what I do when I have a computer program problem which I don't understand (i.e., I don't have a consistent model which explains all the data). Instead of giving up, I try different things and add print statements, hoping to generate enough data to rule out certain types of models and eventually find the right one - even a blind squirrel or a blind search finds an acorn now and then. The important thing is never to give up.

Of course the main point of the post is that this isn't a personal pursuit, but one which uses the time and resources of others, which could be applied elsewhere with more chances of success. So persistence is selfish in this case, but in general it is one of the necessary traits for evolution.

If you're the one who proposes an experiment it's up to you to explain why it's worthwhile. In my area, nobody wants to waste time on this nonsense. I have wasted time by trying to understand the two previous "theories" by Hogan and can tell you why they are wrong. I can't run after the man every time he cooks up something new and tell him why it's wrong. I have rent to pay. This isn't how science works. The proof is up to him to deliver.

I appreciate they had some fun with this equipment. All fine with me. But for me the only outcome is nonsense headlines like this "Good news, we DON’T live in a hologram: Radical experiment dismisses bizarre theory that our world is an illusion." If experimentalists want to test noise backgrounds, that's all fine by me, then they should do this. But stay off my turf if you don't know what you are talking about. How long will it take us to clean up this shit now? If they want to decorate their website with cool words like 'quantum gravity' and 'hologram' then I expect that this is actually the case. This isn't science any more. This is pure marketing.

Oh, yeah, haha. I don't blame Hogan. If you'd hand me money, I would also totally do whatever I want to do and not give a shit what other people think. We're all egocentric and think we can revolutionize physics, all right. I blame Fermilab for making this possible to begin with.

Sabine: "I don't know what makes you think this." Well, when you write a post dismissing research that calls the holographic principle into question, then it creates the impression that you are taking this principle seriously and refusing to accept the negative finding. I can't find anything in your post that dismisses the principle in itself, just this particular experiment. I know you have a head on your shoulders and look askance at any theory that can't be tested, and as I see it, the holographic principle can't be tested, so I would assume you don't take it seriously. But your post is ambiguous, so I can't say for sure. Please reassure me, OK?

Bee, part of the blame also goes to his colleagues outside FNAL (including some LIGO folks with lots of experience in interferometry) for taking part in this. But I guess at one point they thought that the GEO extra noise is pointing to something new.

I don't think it's fair to fault Hogan and the Holometer team for the headline you linked and similar stuff, which reflects the sorry state of science journalism more than anything else. In the paper and quotes from all those involved, all I see is that Hogan proposed a model with a specific observable signature and the experimentalists ruled it out.

If I understand correctly, your more specific critique is that Hogan's model is inconsistent with things we know must be true of quantum gravity; I don't know nearly enough about the subject to agree or contest this. But all the nonsense about holograms and illusions is coming from elsewhere.

I can laugh about this stuff, but that's only because I don't have to make a living at it. I feel for you guys who still have to work the system (and some feel they have to game the system) just to get any work done...

You have a big misunderstanding. Science isn't about testing any hypothesis including those who are already ruled out - this way you just waste resources and we'd never make any progress. The hypotheses that are being put to test are the most promising ones, the ones most likely to teach us something new. To select these, we use peer review. Your attitude of: just give money to anybody with an idea for an experiment is completely unsustainable. Best,

Hogan has been going around for years selling this as a test of the holographic principle and quantum gravity, see articles in Scientific American, New Scientist, and other outlets. He even named the thing holometer. The journalists got their information from a press release of his own institution. How is he not to blame?

I don't blame anybody on his team. I've been in contact with one or two of them I think and they seemed reasonable enough. If there is money in it, of course people will work on it.

Hi Sabine, I have two very naive questions which answers are probably obvious to you.

- How much more precision would we need to detect the gravitational wave of a bullet passing at say 20 cm of one arm?- Guessing there is not enough precision with a single interferometer, would the noise correlation between the two interferometers enable to detect the bullet? (how many ammunition do you need to grow the sigma?)

Essentially, and more generally, the precision is unprecedented; can we imagine something useful to do with the device?

Michelson-Morley is nothing. Folks still look, arXiv:0706.2031. NASA dumped $even figure$ on Podkletnov (cold air is denser than ambient air). Fischbach's "Fifth Force" was nothing. Equivalence Principle composition and spin tests null to one part in 20 trillion relative, still vigorously pursued by rules proven to fail. Nobody tests spacetime geometry with geometry because it violates theory that is curve-fit when it abundantly fails.

Columbus' three ships discovered the New World, the fourth fell off Earth's edge. Worth the look? Yes.

The mainstream of physics is so very troubled in our day. Proceeding by feeling, hunching, intuiting, a glimpse of something when drunk or high or making love that you can't remember now but even so. Fragments of dream last night's REM left 4U: It's all legitimate in its place. Moreover plugs spaces and gaps nothing else can.

The vast majority of great discoveries and advances were hunch driven. Serendipity. There is a high risk attached to individual hunches. The time/cost certainly should not be fronted by institutions, for inexperienced physicists, or those yet to have made a mark, earned a reputation, been promoted to the top of their game. But those that have accomplished those things, have honed an instinct for what is the right way to proceed. They should, and must, be backed their hunches.

Theory always leads...but theory is always there. A well honed hunch when you've reached the top of your game, is a theory.

With that said, I would wish to acknowledge and concede, that what I described which kept true to important historical themes and did deliver for hundreds of years, that none of what I said will change a thing, in the direction of things that you describe. Let alone remedy anything or be a tonic.

This is a bit beyond me, but what of the value of tinkering? Many a strange result from playing around has led to serious discovery. Or is it that this form of tinkering plays havoc with a fair field of play for research funding? I get that the fellow really needs a theory if results are to relate to anything meaningfully, but wonder if his mistakes here might be of some value to others.

“In physics, all theories have to be expressed in form of a consistent mathematical description.”

Are we certain that this is true?

What if the physicist's observable universe is in entirety a zone of dynamic reconciliation between two more fundamental disparate geometries? Is it possible that there is an inherent boundary across which a consistent mathematical description is not possible?

Is there a way of testing the holographic principle? Does Lenny have one?

I thought the holographic principle would prove the Buddhists and Ernst Mach are right to believe that mind or the sensations are the fundamental matter about which we have scientific theory. My visual fields are, I think, two dimensional.

At the very least, we now know that it *doesn't* produce any new or unexplainable results. Failing still means we learned something. One can argue all day that they already knew it wouldn't work, but since when has that stopped humans from trying anyway?